Skeptimediais a commentary on
mass media treatment of issues concerning science, the
paranormal, and the supernatural.

November 18, 2008.
The belief that group therapy can help cancer patients live
longer is widely held by followers of the belief that stress is
a killer we can overcome if only we would relax. This is the
view of both Herbert Benson,
who thinks he made a great discovery called "the relaxation
response," and
David Spiegel, who thinks group therapy can increase the
longevity of breast cancer patients. Spiegel's first study on
the subject was published in 1989 in The Lancet. The
study included 86 women and found that women in group therapy
lived significantly longer than the controls (36.6 months versus
18.9 months). A lot of hoopla followed, but the study needed to
be replicated and when it was the results were quite different.
In 2001, a larger study found no evidence that group therapy
extended the lives of breast cancer patients. Spiegel
rationalized that improvements in conventional cancer treatment
since the 1980s might be masking the independent impact that
group therapy has on the course of disease. He also claimed that
since most patients have probably heard that group therapy
increases longevity, even those assigned to the control group
would look outside the group for social support and group
therapy. Spiegel did a third study, but he is still sitting on
the data because they don't support his hypothesis. He asked for
more funding to extend the study for an additional five years.
That was more than eight years ago.*

Now another study,
led by psychology professor Barbara Andersen of Ohio State
University, has been published that claims "psychological
counseling, muscle relaxation and other strategies for reducing
stress in breast cancer patients can cut their risk of death
from the disease by more than half."*
The study followed 227 women who had lumpectomies or modified
radical mastectomies and tracked them for a median of 11 years.
The women were divided into two groups, one group met with a
pair of psychologists 26 times during the first year after
surgery. The control group didn't meet with psychologists. Both
groups received standard medical follow-up care. The results
were that 19 of the 114 (17%) patients who received counseling died of
breast cancer compared with 25 of the 113 (22%) patients who didn't.
Six more patients, or 2.6% of the whole group, died in the
control group. To claim that these data add up to cutting
anyone's risk of dying of cancer in half seems to be a bit of a
stretch. I don't think the data are robust enough to warrant
claiming there is a causal connection between the counseling and
the fact that there were 5% more deaths in the control group.

The problem with
drawing a grand conclusion that claims breast cancer patients
cut their risk in half by this relaxation therapy is that the
number of women in the study is relatively small, while the
duration of the study is arbitrary. If the researchers follow
the patients for one or two more years, the data might yield a
very different result. If only 2% of the counseling group had
died against 22% of the control group, then these data would be
impressive and would strongly indicate that something besides
chance was going on, though we'd still want to see the study
replicated.

Another example of
misleading statistics in a scientific medical study was published last
week regarding statins. The study involved nearly 18,000 people
worldwide and included men 50 and older and women 60 and older
who did not have high cholesterol or histories of heart
disease. "What they did have was high levels of a protein
called high-sensitivity C-reactive protein, or CRP, which
indicates inflammation in the body."*
(Many scientists believe that inflammation is a better indicator
than cholesterol of who will develop heart disease.)

The study found that
the risk of heart attack was more than cut in half for people
who took statins. The clinical trial, which was designed to last
for five years, was halted after less than two years by an
independent safety monitoring board on the grounds that the
statin is clearly beneficial. But is it? Had the study continued
for the duration, the numbers may have evened out and
problematic side-effects might have proved too many and too
severe to warrant prescribing statins to healthy people.
Ben Goldacre noted that even the present numbers aren't that
impressive:

On placebo, your
risk of a heart attack in the trial was 0.37 events per 100
person years, and if you were taking rosuvastatin [Crestor], it fell to
0.17 events per 100 person years. 0.37 to 0.17. Woohoo. And
you have to take a pill every day. And it might have side
effects.

The vast majority of
those who did not get a statin did quite well. One of the more
important statistics is the
number needed to treat, a measure of how many people need to
be treated for just one person to be helped. Goldacre estimated
that 200 people would have to take the statin to save one life.
The New England Journal (where the study was published)
editorial concluded that treating 120 people for about two years
would help one person. The study authors, using different
criteria, came up with a figure of 95.*

Halting the study
early couldn't have disappointed AstraZeneca, the drug firm that
sponsored the study and supplied the only statin used in the
trial. Rosuvastatin sells for more than $3 a pill. The leader of
the study, Dr. Paul M. Ridker, director of the Center for
Cardiovascular Disease Prevention at Brigham and Women's
Hospital in Boston, said expanding statin use could prevent
about 250,000 heart attacks, strokes, vascular procedures or
cardiac deaths over five years. Ridker is probably not too
unhappy about stopping the study early either. He is one of the
foremost advocates of C-reactive protein testing. That test
runs from $20 to $50 a pop.*

How many people will
suffer side effects, such as liver disease or muscle pain, but not be helped
by taking a daily statin is a statistic I haven't
been able to find. Maybe the researchers weren't looking for it.

You suggest that following 227 patients over a
median of 11 years represents a sample that is too small.

I'm not sure what
rule you use to declare a sample too small, and I'm worried that
you might be dissatisfied with the sample size because of the
conclusion found.

reply: I used the
expression "relatively small" intentionally. I don't claim that
the samples in this study were too
small to be of importance. Elsewhere I've stated that I agree
with the position that a high-caliber controlled study should have
at least 25 in each group in the study.

There are rules
about sample sizes that you can follow. In particular, when you
are observing discrete events, it is the number of events rather
than the number of patients or the amount of follow-up time that
is most important.

One rule is that
you need roughly 25 to 50 events in each group in order to have
reasonable precision. This rule is based on the binomial
distribution, and may be a bit too harsh for survival time data.

Anyway, I think
that having 19 and 25 events respectively is a pretty good (but
not terrific) sample size, though it would help if the
researchers presented confidence intervals rather than p-values.

So what is your
rule for deciding whether a sample size is inadequate?

reply: In this
case, I'd agree that if there were only 2 events (deaths) in the
counseling group versus 25 in the control group, these sample
sizes would be more than adequate to justify some grand
conclusions about the probability of counseling being a
significant causal factor in the outcome. I've rewritten some of
the article to make this point clear.

The other comment
that I felt was unfair was your suggestion that the amount of
follow-up time was arbitrary, and that different follow-up times
might produce different results.

It's certainly
possible that a different follow-up time would produce a
different result. Short term studies tend to overstate the
effectiveness of an intervention, for example. This is a long
term study though (11 years median time is pretty impressive). I
doubt that asking for 13 years of data on average or 9 years of
data on average would lead to markedly different results. You'd
have to have a rather bizarre survival function to produce
markedly different results over such a long time frame.

Certainly if the
median time of follow-up was 6 months, I'd have a problem,
especially since the study couldn't be blinded. Placebo effects
are probably stronger in short term studies.

reply: Again,
maybe I wasn't as clear as I could have been. The difference
between the two groups is pretty small but it might be even
smaller (or larger) if there was a follow-up or two. I've added
a sentence or two that I hope will make it clear why I think the
grand conclusion drawn by the researcher was not justified.

It's possible to
look at the survival curves and speculate what is going on. But
unless the survival curves cross (one group shows superior
results for the first three years and the other group shows
superior results thereafter), I'd not bring up the issue at all.

This is all a
matter of opinion, of course. You can set whatever standard you
like (at least 20 years of follow-up with at least 500 patients
in each group, for example). But I would suggest that such a
standard would be unrealistic and would make force you to ignore
99% of all research studies.

You're on stronger
grounds pointing out that the previous literature is mixed on
the subject. I don't buy the argument that advances in cancer
development have made it harder to show effectiveness of a
psychological intervention. Worst case scenario is that
improvements would lead to fewer people dying, making it harder
to reach the standard of 25 to 50 events per group. But since
the studies are much larger, that's a moot point.

I do enjoy your
newsletter, website, and book, and I hope you take these
comments constructively. -- Steve Simon

reply: Thanks for
giving me the opportunity to clarify a couple of points.